Research Reports POPULATION STUDIES CENTER. Biology Meets Behavior in a Clinical Trial: Two Rela onships between Mortality and Mammogram Receipt

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1 POPULATION STUDIES CENTER Research Reports Report September 2018 Amanda E. Kowalski Biology Meets Behavior in a Clinical Trial: Two Rela onships between Mortality and Mammogram Receipt POPULATION STUDIES CENTER University of Michigan Ins tute for Social Research

2 Biology Meets Behavior in a Clinical Trial: Two Relationships between Mortality and Mammogram Receipt Amanda E. Kowalski University of Michigan University of Michigan Population Studies Center Research Report September 2018 Acknowlegements: Saumya Chatrath, Tory Do, Bailey Flanigan, Pauline Mourot, Dominik Piehlmaier, Ljubica Ristovska, Sukanya Sravasti, and Matthew Tauzer provided excellent research assistance. I thank Anthony Miller, Teresa To, Cornelia Baines, and Claus Wall for sharing data from the Canadian National Breast Screening Study and for answering questions. I thank Magne Mogstad, Atheendar Venkataramani, and seminar participants at the American Economic Association Annual Meeting, the Canadian Health Economics Study Group, the North American Summer Meetings of the Econometric Society, and Princeton for helpful comments. NSF CAREER Award and NIA Grant P30 AG12810 provided support. I dedicate my research on breast cancer to Elisa Long.

3 Abstract I unite the medical and economics literatures by examining relationships between biology and behavior in a clinical trial. Specifically, I identify relationships between mortality and mammogram receipt using data from the Canadian National Breast Screening Study, an influential clinical trial on mammograms. I find two important relationships. First, I find heterogeneous selection into mammogram receipt: women more likely to receive mammograms are healthier. This relationship follows from a marginal treatment effect (MTE) model that assumes no more than the local average treatment effect (LATE) assumptions. Second, I find treatment effect heterogeneity along the mammogram receipt margin: women more likely to receive mammograms are more likely to be harmed by them. This relationship follows from an ancillary assumption that builds on the first relationship. My findings contribute to the literature concerned about harms from mammography by demonstrating variation across the mammogram receipt margin. This variation poses a challenge for current mammography guidelines for women in their 40s, which unintentionally encourage more mammograms for healthier women who are more likely to be harmed by them.

4 1 Introduction The U.S. Preventive Service Task Force (USPSTF) revived the debate on mammography when they updated their mammography guidelines in Although they previously recommended regular mammograms for women in their 40s, the updated guidelines left the mammography decision for women in this age range to individual women and their doctors. The precise USPSTF guidelines for women in their 40s, confirmed in 2016, state: The USP- STF recommends selectively offering or providing this service to individual patients based on professional judgment and patient preferences (U.S. Preventive Service Task Force, 2017). The empirical relationship between which women benefit from mammograms, based on biology, and which women receive mammograms, based on behavior, is crucial to the impact of these guidelines. While the medical literature has focused on biology and the economics literature has focused on behavior, I aim to unite both literatures by examining relationships between the two. The medical literature cited by the USPSTF in its guidelines on mammography (Nelson et al., 2016; Moss et al., 2015; Miller et al., 2014; Tabár et al., 2011; Bjurstam et al., 2003; Frisell et al., 1997; Andersson et al., 1988; Shapiro et al., 1982) focuses on health outcomes from large clinical trials but says little about mammogram receipt behavior. In contrast, the economics literature on mammography focuses on mammogram receipt behavior. It sometimes relates mammogram receipt behavior to health outcomes, but it says little about how variation in mammogram receipt behavior relates to variation in health outcomes (Zanella and Banerjee, 2016; Kadiyala and Strumpf, 2016; Buchmueller and Goldzahl, 2018; Myerson et al., 2018). Kim and Lee (2017) is an exception. Using a regression discontinuity design, they find evidence that women more likely to receive mammograms are healthier, thus identifying a relationship between biology and behavior. I identify two relationships between biology and behavior using data from a clinical trial and a generalized Roy (1951) model of the marginal treatment effect (MTE) as introduced by Björklund and Moffitt (1987), in the tradition of Heckman and Vytlacil (1999, 2001, 2005), Carneiro et al. (2011), and Brinch et al. (2017). I begin with an MTE model that assumes no more than the local average treatment effect (LATE) assumptions of Angrist and Imbens (1994), as shown by Vytlacil (2002). I model behavior in the first stage and relate it to biology in the second stage. In the first stage, differences in behavior determine whether individuals are always takers, compliers, or never takers, in the terminology of Angrist et al. (1996). The model implies that always takers are the first to receive treatment, followed by compliers, and then never takers. In the second stage, differences in outcomes determine whether biology varies with behavior. By comparing average outcomes across always takers, compliers, and never takers, I demonstrate that it is possible to identify two relationships between biology and behavior in existing clinical trial data. The first relationship identifies 2

5 heterogeneous selection into mammography under no ancillary assumptions. The second relationship identifies treatment effect heterogeneity from mammography along the same margin under an ancillary assumption that builds on the first empirical relationship. I apply the model to data from the Canadian National Breast Screening Study (CNBSS), an extensive trial on mammography cited by the USPSTF in its mammography guidelines. The CNBSS enrolled about 90,000 participants between 1980 and In the CNBSS, some participants were randomly assigned to an intervention group that received access to annual mammograms during an active study period, consisting of the enrollment year and 3 to 4 years after enrollment. Remaining participants were assigned to the control group. Control group women in their 40s at enrollment received usual care in the community, and control group women in their 50s at enrollment received annual clinical breast examinations during the active study period. The CNBSS data tracks mammogram receipt in each year of the active study period for all participants, including participants in the control group, allowing me to examine behavior through mammogram receipt. Through linkage to the Canadian Mortality Database, the CNBSS data also tracks mortality for all participants through at least 20 years after enrollment, allowing me to examine biology through mortality. Given the controversy surrounding mammography guidelines for women in their 40s, I focus on women aged at enrollment, representing 50,430 participants, but I examine robustness using the remaining women aged at enrollment. Applying the MTE model to the CNBSS, I identify two relationships between biology and behavior. First, I find that women who are more likely to receive mammograms are healthier. In terms of the MTE model, this is a finding of heterogeneous selection into treatment, where the treatment is mammogram receipt. I identify heterogeneous selection into treatment using a test proposed in the econometric literature by Bertanha and Imbens (2014), Guo et al. (2014), Black et al. (2015) and generalized by Mogstad et al. (2017). This test is also comparable to a test proposed in the insurance literature by Einav et al. (2010). Unlike related tests proposed by Hausman (1978); Heckman (1979); Willis and Rosen (1979); Angrist (2004); Huber (2013), and Brinch et al. (2017), this test does not require any assumptions beyond the LATE assumptions. In Kowalski (2018a,b), I refer to the test as the untreated outcome test because it compares the average untreated outcomes of compliers and never takers, and I show that it identifies heterogeneous selection into treatment. In the CNBSS context, heterogeneous selection into treatment identifies a relationship between biology and behavior. Under an ancillary assumption that builds on the first empirical relationship, I identify a second relationship between biology and behavior. In terms of the MTE model, the second relationship identifies treatment effect heterogeneity along the margin of mammogram receipt. To identify this relationship, I assume weak monotonicity of average untreated out- 3

6 comes along the margin of mammogram receipt. This assumption is weaker than related assumptions made by Olsen (1980), Heckman (1979), and Brinch et al. (2017), as discussed by Kline and Walters (2018). Brinch et al. (2017) impose this assumption in conjunction with a corresponding assumption on treated outcomes to test for treatment effect homogeneity. In Kowalski (2016, 2018b), I demonstrate that either assumption is sufficient. Accordingly, in the CNBSS, I only impose one ancillary assumption. The model imposes the assumption of LATE monotonicity in the first stage, as shown by Vytlacil (2002). The ancillary assumption imposes a corresponding weak monotonicity in the second stage, which implies weak monotonicity of average untreated outcomes from always takers to compliers to never takers. In the context of the CNBSS, the ancillary assumption implies that health, measured by mortality in the absence of mammograms, varies monotonically with mammogram receipt. The direction of the monotonicity depends on the first empirical relationship between mammograms and health. In the CNBSS, the ancillary assumption implies that always takers are weakly healthier than compliers because compliers are healthier than never takers. Covariates collected at baseline provide support for the ancillary assumption. The ancillary assumption implies an upper or lower bound on the average untreated outcome for always takers, which is not observed during the trial. Baseline covariates, which are observed for always takers, can proxy for untreated outcomes. Across several baseline covariates, always takers have higher average socioeconomic status than compliers, who have higher average socioeconomic status than never takers. Therefore, given a positive relationship between socioeconomic status and health without mammograms, health without mammograms should decrease from always takers to compliers to never takers, consistent with the empirical finding and the ancillary assumption. I also find a similar monotonic relationship in baseline health behaviors, providing a potential mechanism. Applying the ancillary assumption to the CNBSS, I obtain an upper bound on average mortality for always takers without mammograms. Because the treatment effect for always takers is the difference between their mortality with and without mammograms, the ancillary assumption also implies a lower bound on the average treatment effect for always takers. The lower bound on the average treatment effect for always takers is larger than the LATE, the average treatment effect on compliers, and they are statistically different from one another. Therefore, the second relationship that I find between biology and behavior in the CNBSS implies that women who are more likely to receive mammograms are more likely to be harmed by them. The possibility that harms of mammograms can outweigh benefits is surprising, but an extensive literature considers the possibility (Bleyer and Welch, 2012; Baum, 2013; Miller et al., 2014; Baines et al., 2016; Nelson et al., 2016; Lannin and Wang, 2017). To illustrate a potential mechanism, suppose that two women receive mammograms. Both are diagnosed 4

7 with breast cancer, and both indeed have breast cancer. Unbeknownst to the women and their doctors, one woman would die within 20 years in the absence of breast cancer treatment, but the other woman would not because her tumor would grow more slowly. Unable to separate the two, both women receive breast cancer treatment, which has its own mortality risks. Both women die within 20 years. The first woman would have died in the absence of breast cancer treatment, so she is neither harmed nor helped. However, the second women would have survived in the absence of breast cancer treatment, so she is harmed. In this example, the harms of mammograms outweigh the benefits on average. My findings, which show that health and the net harms from mammography vary along the mammogram receipt margin, pose a challenge for mammography guidelines. The current USPSTF guidelines for women in their 40s leave the mammography decision to individual women and their doctors. My findings imply that under these guidelines, women more likely to receive mammograms are healthier and more likely to be harmed by them. Beyond the mammography context, my findings demonstrate the importance of examining the relationship between biology and behavior in a world that encourages personalized health care. Fortunately, some relationships between biology and behavior can be identified in existing clinical trial data. In the next section, I begin by replicating previous results from the CNBSS. In Section 3, I apply the MTE model to the CNBSS, and I explain how it relates behavior in the first stage to biology in the second stage. In Section 4, I identify two relationships between biology and behavior using data from the CNBSS. I identify a first relationship between biology and behavior under the model alone. This relationship demonstrates heterogeneous selection into treatment: women more likely to receive mammograms are healthier. Under an ancillary assumption that builds on the first relationship, I identify a second relationship between biology and behavior. This relationship demonstrates treatment effect heterogeneity along the same margin: women more likely to receive mammograms are more likely to be harmed by them. Using covariates collected at baseline, I demonstrate support for the ancillary assumption. I show that my results are robust to a wide variety of alternative specifications in Section 5. I conclude by discussing implications for mammography guidelines and future research in Section 6. 2 Replication of CNBSS Results A great deal has been written on the CNBSS in the medical literature. Viewing the CNBSS as an influential trial, my focus is not to evaluate the CNBSS itself or previous work on it. Rather, my focus is to extend analysis of the CNBSS to examine relationships between mortality and mammogram receipt. Using CNBSS data, I am able to produce an exact replication of the latest result published by CNBSS investigators in Miller et al. (2014), as 5

8 I report in Appendix B. This result shows that access to mammography does not have a statistically significant impact on breast cancer mortality, which is consistent with results published by CNBSS investigators at earlier follow-up lengths (Miller et al., 1992a,b, 1997, 2000, 2002, 2014). This result is are also consistent with other RCT results on mammography considered by the USPSTF in its 2016 mammography guidelines (Nelson et al., 2016). In the replication that serves as the foundation for my extensions, I depart from the exact replication of Miller et al. (2014) in five ways. These departures facilitate further analysis of relationships between mammogram receipt, but they do not have a material impact on the result. In Appendix C, I demonstrate the robustness of the replication across all five departures. First, for consistency with the economics literature, I report the reduced form difference between the intervention and control groups instead of the relative risk ratio. Second, because breast cancer mortality could be endogenous to mammogram receipt and because collateral harms from mammograms could manifest themselves through causes of death that are not reported as breast cancer, I focus on all-cause mortality, which I refer to as mortality for simplicity. Third, for ease of interpretation, I report results at the maximal follow-up length of 20 years after enrollment for all subjects instead of reporting results at a fixed follow-up cutoff. Fourth, because the USPSTF guidelines changed specifically for women in their 40s, I only include women aged in my main analysis sample and examine the robustness of my results for women aged Fifth, to focus on relationships between mortality and mammogram receipt for women with no known clinical reasons to receive a mammogram before randomization occurred, I exclude women from my analysis sample if they have any nonzero values of the following breast-related covariates at baseline: breast cancer in family; any other breast disease; patient reported symptoms; referred for review by nurse; abnormality found by nurse; ever told has breast cancer. I examine the robustness of my results to these sample restrictions. My main analysis sample includes 19,505 women. 3 Model I use an MTE model to identify two relationships between biology and behavior in the CNBSS. I follow the exposition from Kowalski (2018a) closely, making only stylistic changes to the model used by Heckman and Vytlacil (2005) to ensure that the model assumes no more than the LATE assumptions of Angrist and Imbens (1994), as shown by Vytlacil (2002). Applying the model to the CNBSS, I model behavior in the first stage, and I relate biology to behavior in the second stage. 3.1 Behavior: Mammogram Receipt In the context of the CNBSS, I use treatment to refer to mammogram receipt, which I represent with D. I define mammogram receipt D such that D = 1 if a participant receives 6

9 a mammogram in at least one year after enrollment during the active study period, and I set D = 0 otherwise. If mammogram data is missing in any year, I construct D such that the participant did not receive a mammogram in that year. Let V T represent potential utility in the treated state, the state with mammogram receipt, and let V U represent potential utility in the untreated state, the state without mammogram receipt. I relate both potential utilities to realized utility V such that: V = V U + (V T V U )D. (1) I specify the potential utilities as follows: V T = µ T (Z, X) + ν T (2) V U = µ U (Z, X) + ν U, (3) where µ T ( ) and µ U ( ) are unspecified functions, X is an optional vector of observed covariates, Z is an observed binary instrument, and ν T and ν U are unobserved terms with unspecified distributions. In the CNBSS, the instrument represents random assignment to the intervention group such that Z = 1 for intervention group participants and Z = 0 for control group participants. I assume: A.1. (First Stage Independence) The random variable ν U ν T is independent of Z conditional on X, which implies that F (ν U ν T X), denoted as U D, is independent of Z conditional on X. A.2. (First Stage Technical Assumption) The cumulative distribution function of ν U ν T conditional on X, which I denote with F, is continuous and strictly increasing. These assumptions imply the following equation for mammogram receipt conditional on random assignment: D = 1{U D P(D = 1 Z = z, X)}, (4) where U D = F (ν U ν T X). I show for completeness in Appendix A.1 that this equation follows from the statement that participants receive mammograms if and only if their potential treated utility V T exceeds their potential untreated utility V U. Equivalently, under the mammogram receipt equation (4), participants receive mammograms if their values of U D are less than the threshold P(D = 1 Z = z, X). As I show for completeness in Appendix A.2, the model implies that U D is distributed uniformly between 0 and 1. I interpret U D as the unobserved net cost of treatment, where the net cost is equal to the cost minus the benefit. In the CNBSS context, participants with the lowest unobserved net cost of mammogram receipt receive mammograms first. 7

10 There are two special cases of the mammogram receipt equation (4) for intervention and control group participants: D = 1{U D p CX } where p CX = P ( D = 1 Z = 0, X), (5) D = 1{U D p IX } where p IX = P ( D = 1 Z = 1, X), (6) where the probabilities p CX and p IX can be estimated in the control group (Z = 0) and the intervention group (Z = 1), respectively. It is always possible to rename the intervention group as the control group and vice versa to satisfy p CX p IX. I therefore proceed with p CX p IX. I make the following assumptions, which are verifiable: A.3. (First Stage Relevance) µ T (Z, X) µ U (Z, X) is a nondegenerate random variable conditional on X. A.4. (First Stage Mammogram Receipt Differs from Random Assignment with Positive Probability) 0 < P(D = 1 Z = z, X) < 1. Under these assumptions, I partition the mammogram receipt margin U D into distinct ranges. I depict the ranges in Figure 1. The top line depicts the ranges for control group participants. In my main analysis sample from the CNBSS, 19% of control group participants receive mammograms, so p C = 0.19, where I suppress X to indicate that p C represents an average in the full sample, not in a sample conditional on X. By (5), control group participants that receive mammograms have 0 U D These participants must be always takers. The middle line of Figure 1 depicts ranges of U D for intervention group participants. In my main analysis sample from the CNBSS, 95% of intervention group participants receive mammograms, so p I = By (6), intervention group participants that do not receive mammograms have 0.95 < U D 1. These participants must be never takers. I depict U D for participants in the control and intervention group on same axis in the bottom line of Figure 1. Participants in the middle range (0.19 < U D 0.95) receive mammograms if and only if they are in the intervention group, so they must be compliers. The depiction in the bottom line of Figure 1 is consistent with the ordering from always takers to compliers to never takers originally shown by Vytlacil (2002). In the CNBSS, this ordering identifies variation in behavior along the mammogram receipt margin: always takers receive mammograms first, followed by compliers, followed by never takers. 8

11 Figure 1: Ranges of U D for Always Takers, Compliers, and Never Takers Z=0 Z=1 D=1 D=0 D=1 D=0 0 p C = p I = 0.95 Always Takers Compliers Never Takers 3.2 Biology: Mortality U D : unobserved net cost of treatment I relate mammogram receipt D to mortality Y as follows: Y = Y U + (Y T Y U )D. (7) I specify treated mortality Y T and untreated mortality Y U such that: Y T = g T (X, U D, γ T ) (8) Y U = g U (X, U D, γ U ), (9) where g T ( ) and g U ( ) are unspecified functions that need not be additively separable in their observed an unobserved components, unlike the potential utility functions in (2) and (3). X is the same optional vector of observed covariates from the first stage of the model, U D is the unobserved net cost of treatment from the first stage of the model, and γ T and γ U are unobserved terms with unspecified distributions. I assume: A.5. (Second Stage Independence) The random vector (U D, γ T ) and the random vector (U D, γ U ) are independent of Z conditional on X. Under this final assumption, the model is equivalent to the LATE assumptions. 3.3 Biology and Behavior: Mortality and Mammogram Receipt The model relates behavior to biology, as I show graphically in Figure 2. The horizontal axis depicts behavior via the mammogram receipt margin U D, and the vertical axis depicts biology via mortality. Over the relevant ranges of the horizontal axis, I depict average outcomes that I obtain using the model, as I detail algebraically in Appendix A.3 and graphically in Appendix D. Imbens and Rubin (1997), Katz et al. (2001), Abadie (2002), and Abadie (2003) show how to obtain the same average outcomes using the LATE assumptions. In Figure 2, I use dotted lines to represent average treated outcomes. As shown, 20 years after enrollment, always takers (0 U D p C ) experienced 451 deaths per 10,000 9

12 Figure 2: Biology and Behavior: Average Mortality for Always Takers, Compliers, and Never Takers Under the LATE Assumptions All-Cause Deaths 20 Years After Enrollment (per 10,000) treated untreated LATE = -13 (38) 0 p c = 0.19 p I = Always Takers Compliers Never Takers U D : unobserved net cost of treatment Note. Bootstrapped standard errors in parentheses. All-cause deaths are measured 20 years after enrollment for all participants, based on the exact calendar date of enrollment. The treatment is mammogram receipt, which is equal to one if a participant receives a mammogram in at least one year after enrollment during the active study period. Missing mammogram data in any year is set to no mammogram in that year. The sample includes women aged at enrollment, excluding women with any nonzero values of the following breast-related covariates at baseline: breast cancer in family; any other breast disease; patient reported symptoms; referred for review by nurse; abnormality found by nurse; ever told has breast cancer. participants, while treated compliers (p C U D p I ) experienced 415 deaths per 10,000 participants. I use dashed lines to represent average untreated outcomes. Over the same time period, untreated compliers (p C U D p I ) experienced 428 deaths per 10,000 participants and never takers (p I U D 1) experienced 990 deaths per 10,000 participants. As I emphasize in Figure 2, average untreated outcomes are not observed for always takers, and average treated outcomes are not observed for never takers. As originally shown by Imbens and Rubin (1997), the LATE is equal to the difference between the average treated and untreated outcomes for compliers. In Figure 2, I depict the 10

13 LATE with an arrow. The LATE is not statistically different from zero, but its magnitude indicates that compliers experienced an average decrease of 13 deaths per 10,000 participants. The LATE is also equal to the reduced form reported in Table A.2 divided by the first stage ( -10 / ( ) = -13). The depiction in Figure 2 makes clear that the LATE represents the average treatment effect on compliers but that always and never takers make up a substantial fraction of the sample, leaving room for the possibility of selection and treatment effect heterogeneity. Within the model, I characterize selection and treatment effect heterogeneity along the entire margin of mammogram receipt using functions from the MTE literature (see Carneiro and Lee, 2009; Brinch et al., 2017): Marginal Untreated Outcome (MUO): MUO(x, p) = E [Y U X = x, U D = p] (10) Marginal Treated Outcome (MTO): MTO(x, p) = E [Y T X = x, U D = p] (11) Marginal Treatment Effect (MTE): MTE(x, p) = E [Y T Y U X = x, U D = p] (12) where x is a realization of the covariate vector X and p is a realization of the unobserved net cost of treatment U D. In the context of the CNBSS, these functions relate biology to behavior along the entire mammogram receipt margin U D. In Kowalski (2016, 2018a,b), I refer to the first function as the marginal treated outcome (MUO) function, and I refer to the second function as the marginal untreated outcome (MTO) function. The difference between the MTO function and the MUO function yields the marginal treatment effect (MTE) function of Heckman and Vytlacil (1999, 2001, 2005). In Kowalski (2018a), I show that the MUO function characterizes selection heterogeneity along U D. As I show in Appendix A.4, a definition of selection heterogeneity used in the econometrics literature can be obtained as a weighted integral of the MUO function. Relative to definitions used in the literature, the MUO function is more general, and it does not depend on the fraction of individuals assigned to the intervention group, which is a feature of the experimental design. Intuitively, variation in average untreated outcomes across U D can only be due to selection heterogeneity; it cannot be due to treatment effect heterogeneity because only treated outcomes can reflect treatment effects. In the CNBSS, the MUO function characterizes how selection on mortality changes along the mammogram receipt margin. Therefore, it characterizes a first relationship between biology and behavior in the CNBSS. In Kowalski (2018a), I show that the MTO function characterizes the sum of selection and treatment effect heterogeneity along U D. In contrast to average untreated outcomes, which can only reflect selection heterogeneity, average treated outcomes can reflect selection heterogeneity, treatment effect heterogeneity, or both. It is tempting to think that treated outcomes and untreated outcomes can be interchanged without consequence, but the treat- 11

14 ment effect is defined as the treated outcome minus the untreated outcome, not the untreated outcome minus the treated outcome. Therefore, the treatment effect has magnitude and direction. Renaming the untreated outcome as the treated outcome and vice versa would change the direction of the treatment effect, illustrating why there is a material distinction between treated and untreated outcomes. The MTE function characterizes treatment effect heterogeneity along U D. As I show in Kowalski (2018a) and in Appendix A.4, a definition of treatment effect heterogeneity used in the econometrics literature can be obtained as a weighted integral of the MTE function. In the CNBSS, the MTE function characterizes how the impact of mammography on mortality changes along the mammogram receipt margin. Therefore, it characterizes a second relationship between biology and behavior in the CNBSS. 4 Results: Two Relationships Between Mortality and Mammogram Receipt Applying MTE methods to the CNBSS, I identify two main relationships between biology and behavior. First, under the model that assumes no more than the LATE assumptions, I find selection heterogeneity: women who are more likely to receive mammograms are healthier. Second, under an ancillary assumption, I find treatment effect heterogeneity along the margin of mammogram receipt: women more likely to receive mammograms are more likely to be harmed by them. 4.1 Selection Heterogeneity on Mortality Along the Margin of Mammogram Receipt I test for selection homogeneity using the following test statistic, which gives the difference in average mortality without mammograms between compliers (p C < U D p I ) and never takers (p I < U D 1): E[Y U p C < U D p I ] E[Y U p I < U D 1] = 1 0 (ω(p, p C, p I ) ω(p, p I, 1)) MUO(p) dp, where ω(p, p L, p H ) = 1{p L p < p H }/(p H p L ). The test of the null hypothesis that this test statistic is equal to zero is equivalent to or similar to tests proposed by Bertanha and Imbens (2014), Guo et al. (2014), and Black et al. (2015), which are generalized by Mogstad et al. (2017). It is also comparable to a test proposed in the insurance literature by Einav et al. (2010). In Kowalski (2018a,b), I refer to the test as the untreated outcome test because it compares average untreated outcomes, and I show that it identifies a special case of selection heterogeneity. Intuitively, because never takers and compliers without mammograms (13) 12

15 Figure 3: Untreated Outcome Test Shows Negative Selection Heterogeneity Under the LATE Assumptions All-Cause Deaths 20 Years After Enrollment (per 10,000) treated untreated untreated outcome test: = -562 (147) LATE = -13 (38) 0 p c = 0.19 p I = Always Takers Compliers Never Takers U D : unobserved net cost of treatment Note. Bootstrapped standard errors in parentheses. All-cause deaths are measured 20 years after enrollment for all participants, based on the exact calendar date of enrollment. The treatment is mammogram receipt, which is equal to one if a participant receives a mammogram in at least one year after enrollment during the active study period. Missing mammogram data in any year is set to no mammogram in that year. The sample includes women aged at enrollment, excluding women with any nonzero values of the following breast-related covariates at baseline: breast cancer in family; any other breast disease; patient reported symptoms; referred for review by nurse; abnormality found by nurse; ever told has breast cancer. are untreated, a difference in their average outcomes can only reflect selection heterogeneity. A negative test statistic indicates negative selection heterogeneity, and a positive test statistic indicates positive selection heterogeneity. Using algebra, (13) demonstrates that the untreated outcome test identifies a special case of selection heterogeneity because the test statistic can be obtained as a weighted integral of the MUO function, which characterizes selection heterogeneity over the entire selection margin. Applying the untreated outcome test to data from the CNBSS, I find that never takers experienced 562 more deaths per 10,000 participants than untreated compliers, as depicted in Figure 3. The standard error of 147 indicates that the difference is statistically different 13

16 from zero. Therefore, I can reject selection homogeneity. The sign of the untreated outcome test statistic indicates that women more likely to receive mammograms are less likely to die from any cause 20 years after enrollment. Using mortality as a measure of health, I find the first of two relationships between biology and behavior in the CNBSS: women more likely to receive mammograms are healthier. This selection heterogeneity is consistent with the results of Kim and Lee (2017), who find evidence that women more likely to receive mammograms are healthier using a regression discontinuity design. 4.2 Treatment Effect Heterogeneity on Mortality Along the Margin of Mammogram Receipt To test for treatment effect heterogeneity, I impose the following ancillary assumption: M.1. (Weak Monotonicity of the MUO Function) For all p 1, p 2 [0, 1] such that p 1 < p 2 : E[Y U U D = p 1 ] E[Y U U D = p 2 ] or [Y U U D = p 1 ] E[Y U U D = p 2 ]. Brinch et al. (2017) impose this assumption in conjunction with an analogous assumption on the MTO function to test for treatment effect homogeneity. In Kowalski (2016, 2018b), I demonstrate that either assumption is sufficient. Weak monotonicity of the MUO function implies weak monotonicity of average untreated outcomes from always takers, to compliers, to never takers. Accordingly, in the CNBSS, I only impose Assumption M.1, which assumes weak monotonicity of the MUO function. In Appendix E, I present alternative weak monotonicity assumptions on the MTO and MTE functions, and I discuss why I do not impose them in the CNBSS. While the model imposes LATE monotonicity in the first stage, as shown by Vytlacil (2002), these assumptions impose corresponding weak monotonicities in the second stage. In the context of the CNBSS, Assumption M.1 implies that average health, measured by mortality in the absence of mammograms, varies monotonically from always takers to compliers to never takers. The direction of the monotonicity depends on the first empirical relationship between mammogram receipt and health. In the CNBSS, compliers are healthier than never takers on average, so the ancillary assumption implies that always takers are weakly healthier than compliers on average. As illustrated in Figure 4, Assumption M.1 implies that always takers without mammograms would face no more than 428 deaths per 10,000 participants. Under Assumption M.1, I test the null hypothesis of treatment effect homogeneity using the following decision rule, which has an outcome that is equal to 1 if the test rejects 14

17 treatment effect homogeneity and 0 otherwise: E[Y T 0 U D < p C ] E[Y U p C < U D p I ] > E[Y T Y U p C U D p I ] if E[Y U p C < U D p I ] E[Y U p I < U D 1] 0, 1 E[Y T 0 U D < p C ] E[Y U p C < U D p I ] < E[Y T Y U p C < U D p I ] if E[Y U p C < U D p I ] E[Y U p I < U D 1] > 0. (14) As shown, this decision rule has two cases, which depend on the sign of the untreated outcome test statistic. If the untreated outcome test statistic is negative, then untreated compliers die at a lower rate than never takers. In this case, under Assumption M.1, average mortality for untreated compliers represents an upper bound on the average untreated mortality of always takers. I can therefore derive a lower bound on the average treatment effect of always takers that I can compare to the LATE to evaluate treatment effect homogeneity. Because the lower bound on the average treatment effect for always takers is strictly greater than the LATE, the average treatment effect for always takers cannot be equal to the LATE. However, if the untreated outcome test statistic were positive, then average mortality for untreated compliers would represent a lower bound on the average untreated outcome of always takers. Hence, I would derive an upper bound on the average treatment effect of always takers that must be strictly less than the LATE to reject treatment effect homogeneity. Applying the test to the CNBSS, I reject treatment effect homogeneity. As reported in Figure 4, under Assumption M.1, I derive a lower bound on the average treatment effect of always takers that indicates that always takers experience at least an additional 22 deaths per 10,000 participants when they receive mammograms. The lower bound on the average treatment effect for always takers is strictly greater than the LATE, so always takers face a strictly greater average treatment effect than compliers. Therefore, the decision rule yields a value of one, and I can reject treatment effect homogeneity in the CNBSS as reported in column (4) of Table 2. The standard error of 0.48 shows that average treatment effects for always takers and compliers are statistically different from one another. Furthermore, the direction of heterogeneity in the average treatment effect indicates that women more likely to receive mammograms are more likely to be harmed by mammograms. This finding seems surprising at first. However, anecdotal evidence from a clinical nurse suggest a potential mechanism: I never, though, had a patient whose worry about those side effects came close to her worry about the disease. Being preoccupied with saving ones life produces a myopia, in which other worries unrelated to ones possibly imminent death fall away. (Brown, 2017). Healthier women might be more susceptible to this type of myopia because breast cancer represents a larger shock to their health. Given their fear of the disease, they might undertake more aggressive surgeries and treatments. Consequently, 15

18 Figure 4: Test Rejects Treatment Effect Homogeneity Under the Ancillary Assumption of Weak Monotonicity of the MUO Function and the LATE Assumptions treated untreated All-Cause Deaths 20 Years After Enrollment (per 10,000) treatment effect lower bound = 22 (59) upper bound test rejects treatment effect homogeneity: 1{22 > 13} = 1.00 (0.48) LATE = -13 (38) 0 p c = 0.19 p I = Always Takers Compliers Never Takers U D : unobserved net cost of treatment Note. Bootstrapped standard errors in parentheses. All-cause deaths are measured 20 years after enrollment for all participants, based on the exact calendar date of enrollment. The treatment is mammogram receipt, which is equal to one if a participant receives a mammogram in at least one year after enrollment during the active study period. Missing mammogram data in any year is set to no mammogram in that year. The sample includes women aged at enrollment, excluding women with any nonzero values of the following breast-related covariates at baseline: breast cancer in family; any other breast disease; patient reported symptoms; referred for review by nurse; abnormality found by nurse; ever told has breast cancer. Some differences between statistics might not appear internally consistent because of rounding. they could be more likely to experience collateral harms from mammography Support for the Ancillary Assumption Using Baseline Covariates I investigate support for the ancillary assumption in the CNBSS using covariates collected at baseline. The ancillary assumption implies an upper or lower bound on the average untreated outcome for always takers, which is not observed during the trial. Baseline covariates, which are observed for always takers, can proxy for their untreated outcomes. I begin by examining variation in baseline covariates related to socioeconomic status 16

19 because socioeconomic status is known to be inversely correlated with mortality (Pappas et al., 1993; Cutler and Lleras-Muney, 2010; National Center for Health Statistics, 2012). Specifically, I compare average characteristics at baseline across always takers, compliers, and never takers in Table 1. I detail how I obtain average characteristics for compliers in Appendix A.5. Covariates related to socioeconomic status show a general pattern of monotonic variation from always takers to compliers to never takers, with always takers having the highest socioeconomic status. Furthermore, covariates related to health behaviors such as smoking status, body mass index, and mammograms prior to enrollment suggest a monotonic relationship across always takers, compliers, and never takers, where always takers exhibit the best health behaviors. Therefore, variation in baseline socioeconomic status and health behavior supports the assumption that average health decreases from always takers to compliers to never takers. Table 1: Baseline Summary Statistics for Always Takers, Compliers, and Never Takers Means Difference in Means (1) (2) (3) Always Never Takers Compliers Takers (1)-(2) (2)-(3) Baseline Socioeconomic Status University, trade or business school (0.01) (0.01) (0.02) (0.01) (0.02) In work force (0.01) (0.00) (0.02) (0.01) (0.02) Age at first birth (0.12) (0.05) (0.21) (0.14) (0.22) No live birth (0.01) (0.00) (0.01) (0.01) (0.02) Married (0.01) (0.00) (0.02) (0.01) (0.02) Husband in work force / alive (0.01) (0.00) (0.02) (0.01) (0.02) Baseline Health Behavior Non-Smoker (0.01) (0.00) (0.02) (0.01) (0.02) Body Mass Index (0.10) (0.05) (0.21) (0.12) (0.22) Used oral contraception (0.01) (0.00) (0.02) (0.01) (0.02) Used estrogen (0.01) (0.00) (0.02) (0.01) (0.02) Mammograms prior to enrollment (0.01) (0.00) (0.02) (0.01) (0.02) Practiced breast self examination (0.01) (0.00) (0.02) (0.01) (0.02) Note. Bootstrapped standard errors in parentheses. Missing values correspond to redacted numbers in accordance with Data Use Agreement. The treatment is mammogram receipt, which is equal to one if a participant receives a mammogram in at least one year after enrollment during the active study period. Missing mammogram data in any year is set to no mammogram in that year. The sample includes women aged at enrollment, excluding women with any nonzero values of the following breast-related covariates at baseline: breast cancer in family; any other breast disease; patient reported symptoms; referred for review by nurse; abnormality found by nurse; ever told has breast cancer. Baseline breast-related covariates are not reported here because they are all zero based on the sample restriction. Some differences between statistics might not appear internally consistent because of rounding. 17

20 5 Robustness I examine the robustness of the two empirical relationships that I find between biology and behavior along many dimensions. Specifically, I examine alternative subsamples, alternative definitions of mammogram receipt, and alternative outcomes. Although I focus on women aged at enrollment, I also examine results for women aged at enrollment. To facilitate comparisons with the main specification, I present tables that summarize the main results from Figures 2, 3, and 4, starting with Table 2. Column (1) reports the LATE. Column (2) reports the untreated outcome test statistic, which identifies the first relationship between biology and behavior: selection heterogeneity. When the untreated outcome test statistic is negative and statistically different from zero, this relationship shows that women more likely to receive mammograms are healthier. Column (4) reports the outcome of the decision rule in (14), which identifies the second relationship between biology and behavior: treatment effect heterogeneity. When the untreated outcome test statistic is negative, as it is in the main specification and almost all reported alternative specifications, column (3) gives a lower bound on the average treatment effect for always takers. If the lower bound in column (3) is greater than the LATE in column (1), then the average treatment effect on always takers must exceed the treatment effect on compliers. In this case, a rejection of treatment effect heterogeneity in column (4) indicates that women more likely to receive mammograms are more likely to be harmed by them. 5.1 Alternative Subsamples Alternative Subsample Based on Breast-Related Covariates at Baseline I investigate robustness of my results to the exclusion of participants with any nonzero breast-related covariates at baseline. To do so, I examine the subsample that only includes participants removed by this restriction and the full sample without this restriction. I begin by comparing baseline covariates across always takers, compliers, and never takers in the two samples in Tables A.5 and A.6 of Appendix F. Even in the sample of women with any nonzero breast-related covariates at baseline, covariates that measure socioeconomic status and health behavior lend support to the assumption that women more likely to receive mammograms are healthier. The breast-related covariates themselves suggest the opposite relationship. However, the breast-related covariates could be endogenous to breast cancer screening that occurred before the CNBSS began, especially since always takers report prior mammograms and breast self examination at a meaningfully higher rate than compliers. Nonetheless, the exclusion of women with any baseline breast-related covariates from the main analysis sample is conservative. In Table 2, I summarize results in the alternative samples that include women with any nonzero breast-related covariates. In Appendix G, I report the full results necessary 18

21 to construct analogous versions of Figures 1-2 for the alternative samples. As shown, the untreated outcome test is negative and the test rejects treatment effect heterogeneity in both alternative samples, so the main results are robust. Table 2: Alternative Samples and Outcomes (1) (2) (3) (4) Local Average Untreated Always Taker Test Rejects Treatment Effect Outcome Treatment Effect Treatment Effect N LATE Test Lower Bound Homogeneity Main Specification Main specification 19, (38) (147) (59) (0.48) Alternative Subsample Based on Breast-Related Covariates Any nonzero breast-related covariates 30, (40) (135) (39) (0.47) Both zero and nonzero breast-related covariates 50, (27) (103) (31) (0.34) Alternative Outcomes Breast cancer mortality 19, (13) (47) (25) (0.43) Breast cancer incidence 19, (34) (119) (65) (0.17) Alternative Sample Based on Age Group Participants Aged at Enrollment 17, , (60) (226) (103) (0.20) Note. Bootstrapped standard errors in parentheses. The treatment is mammogram receipt, which is equal to one if a participant receives a mammogram in at least one year after enrollment during the active study period. Missing mammogram data in any year is set to no mammogram in that year. Baseline breast-related covariates refer to the following: breast cancer in family; any other breast disease; patient reported symptoms; referred for review by nurse; abnormality found by nurse; ever told has breast cancer. Some differences between statistics might not appear internally consistent because of rounding Alternative Subsamples Based on Enrollment Year and Center I examine robustness of my findings in subsamples based on enrollment year in Appendix H and CNBSS center in Appendix I. In all but two of the 21 subsamples, women more likely to receive mammograms are healthier. This relationship is statistically different from zero in most subsamples, even though sample sizes shrink dramatically. Furthermore, in all but one of the subsamples by enrollment year in which I find the first relationship, I also find the second relationship: I reject treatment effect homogeneity such that women more likely to receive mammograms are more likely to be harmed by them. The subsamples by CNBSS center are generally smaller than the subsamples by enrollment year, but I still find the second relationship in many of them. 5.2 Alternative Definitions of Mammogram Receipt In the CNBSS, I define mammogram receipt D such that D = 1 if a participant receives a mammogram in at least one year after enrollment during the active study period and I set D = 0 otherwise. If mammogram data is missing for a given participant in a given year, I construct D such that the participant did not receive a mammogram in that year. In Tables 3 19

22 and Appendix J, I consider narrower and broader definitions of mammogram receipt. Under the narrowest definition, participants must receive a mammogram in all active study period years after enrollment to be considered treated. Under the broadest definition, participants must receive a mammogram or be missing mammogram data in any active study period year after enrollment to be considered treated. The narrowest and broadest definitions are arguably too extreme, so it is notable that all reported specifications yield point estimates consistent with the first relationship from the main specification: women more likely to receive mammograms are healthier. Because this relationship holds, the reported results do not contradict the second relationship from the main specification, even in the two reported specifications in which the test does not reject treatment effect heterogeneity. To contradict the second relationship, implying that women more likely to receive mammograms are less likely to be harmed by them, the untreated outcome test would have to be positive and the test reported in the last column would have to reject treatment effect heterogeneity. Table 3: Alternative Definitions of Mammogram Receipt (1) (2) (3) (4) Local Average Untreated Always Taker Test Rejects Treatment Effect Outcome Treatment Effect Treatment Effect N LATE Test Lower Bound Homogeneity Main Specification Mammogram in at least one year after enrollment during the active study period, missing in year = no mammogram in year Main specification 19, (38) (147) (59) (0.48) Narrower Definitions of Mammogram Receipt Mammogram in more than one year after enrollment during the active study period, missing in year = no mammogram in year At least two active study period years 19, (35) (106) (77) (0.49) At least three active study period years 19, (36) (94) (145) (0.48) All active study period years 19, (42) (75) (138) (0.37) Broader Definitions of Mammogram Receipt Mammogram in at least one year after enrollment during the active study period Missing in year = mammogram in year 19, (69) (835) (43) (0.43) Note. Bootstrapped standard errors in parentheses. All-cause deaths are measured 20 years after enrollment for all participants, based on the exact calendar date of enrollment. The treatment is mammogram receipt. In the main specification, mammogram receipt is equal to one if a participant receives a mammogram in at least one year after enrollment during the active study period. Missing mammogram data in any year is set to no mammogram in that year. The sample includes women aged at enrollment, excluding women with any nonzero values of the following breast-related covariates at baseline: breast cancer in family; any other breast disease; patient reported symptoms; referred for review by nurse; abnormality found by nurse; ever told has breast cancer. Some differences between statistics might not appear internally consistent because of rounding. 20